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Monday, August 25, 2014

A Universal Basic Income and Work Incentives: What Does the Empirical Evidence Tell Us?

In Part 1 of this series,
I outlined some basic economic theory regarding a universal basic
income (UBI) and work incentives. By a UBI, I mean an income support
policy that provides a set monthly benefit to every citizen. A UBI, as I
define it, would to everyone, regardless of income, wealth, or
employment status. In that respect it differs from means-tested income
support policies (MTIS), such as current US welfare system programs or a
negative income tax (NIT), which reduce benefits as the recipient’s
income increases.

The fear that a UBI would undermine work
incentives is among the most important sources of resistance to the
idea. In Part 1, I argued, on theoretical grounds, that replacing the
existing welfare system with a UBI would tend to increase average work
effort. This part will look at several sources of evidence that support
the theory, beginning with the famous income maintenance experiments
(IMEs) of the 1970s and 1980s.

What we can learn from the IMEs and what we can’t learn

The
income maintenance experiments in question followed a method known as
randomized field trials. Each of the experiments enrolled from several
hundred to several thousand households and divided them into two groups.
They assigned one group to an experimental income support policy while a
control group continued to be covered by existing welfare programs,
including Aid for Families with Dependent Children (AFDC), food stamps,
and others. IMEs testing various policies took place in New Jersey,
Iowa, North Carolina, Indiana, Colorado, and Washington. They covered
both urban and rural areas; both single parent and two-parent
households; and various ethnic groups.

UBI critics have pointed to the IMEs
as a key source of evidence about the work incentive effects of a UBI. As Pascal-Emmanuel Gobry
puts it:

Science, properly understood, is the
testing of hypotheses through rigorous experimentation. This is not what most
published social science studies do. . . There is, however, one way to
gain relatively reliable social-scientific evidence: randomized field trials. .
. The UBI is one of the very few, if not the only, domains of social science
policy where we have exactly that: extensive, long-term, repeated RFTs, which
are the gold standard of evidence in social science.

It is important, then, to understand
exactly what these experiments can and can’t tell us. Let’s begin with a key negative:
We can learn nothing directly from the IMEs about the effects of a UBI because
they did not test such a policy.

Instead, the IMEs tested several
variants of a negative income tax. An NIT and a UBI are not the same thing. As
explained in Part 1, an NIT is means-tested. All versions of the NITs tested in
the IMEs incorporated substantial benefit reduction rates, ranging from 30 to
80 percent. In contrast, a UBI has no benefit reductions. It would be fair to
say, then, that the IMEs offer no direct evidence about the effects of a UBI,
any more than a clinical trial of the effects of vitamin C on heart attacks
would offer evidence about the protective effects of aspirin.

The confusion between a UBI and an
NIT is partly a matter of terminology. In a recent essay for Cato Unbound, Matt Zwolinski employs another term, Basic Income
Guarantee (BIG), to refer to a broader family of income support programs
that have the common feature of guaranteeing a minimum level of income to
everyone. A UBI, as I have defined it, is the most "universal" member
of the BIG family in the sense that everyone gets the full payment regardless
of income, wealth, or work status with no benefit reductions. In addition,
BIGs, as Zwolinski defines them, also include NIT policies such as Milton
Friedman’s early version, the NIT variants tested in the IMEs, and related programs
like a plan advanced by Charles Murray
. All of these policies include provisions that reduce the basic benefit by a
fraction of a dollar for each dollar earned, beyond some defined amount.

Critics have not always been careful
to distinguish between a UBI and an NIT, nor have they consistently recognized
that the two have different incentive effects. For example, Manzi, in responding
to Zwolinski’s arguments for a BIG, simply recycles a set of arguments that he
used in an earlier National Review article about a negative income tax. In doing so, he claims
that the IMEs of the 1970s and 1980s showed “every tested variant of a BIG to
have pernicious effects” on work incentives. That contention is literally true,
inasmuch as all the “tested variants” were one or another formulation of a
negative income tax. What Manzi fails to note is that none of the IMEs tested a
true UBI.

Let’s turn now to the positives—to
what we can hope to learn from the IMEs. The first thing would be something
about the incentive effects of a negative income tax.

As Gobry, Manzi, and other critics
point out, the raw data from the IMEs show that almost all experimental groups
reduced their average work efforts compared to their controls. Gary Burtless
of the Brookings Institution summarizes the data in Table 2 of a paper that he
prepared for a 1986 conference
sponsored by the Boston Fed. The table shows that husbands reduced their work
by an average of 119 hours per year, wives by an average of 93 hours, and
single female heads of households by an average of 133 hours per year. Only two
subgroups, black husbands in New Jersey and black wives in Gary, Indiana,
increased their work compared to their control groups.

Those results concerning the effects
of an NIT should come as no surprise to anyone who has read Part 1 of this
series. In Figure 2 of Part 1, we saw that “sweetening” an existing
means-tested welfare scheme by increasing the minimum income guarantee and
reducing the benefit reduction rate would produce ambiguous results. Some
participants would increase their work efforts and others would cut back. The greater
the increase in the minimum income guarantee, the more likely a reduction in
average work effort, because of the income effect. The greater the decrease in
the benefit reduction rate, the more likely an increase in work effort, because
of the substitution effect. Also, an increase in either parameter would
increase the number of people eligible for the program, thereby potentially
reducing the work effort of people who previously had incomes just above the
new cutoff level.

Interpretation of the raw data on
work responses is complicated by fact that the NIT plans faced by the
experimental groups included variations in both the minimum income guarantee
and the benefit reduction rate. Furthermore, the tested NITs were not always
“sweeter” in both respects compared to the welfare policies available to their
respective control groups. Some experimental groups received minimum income
guarantees of as much as 135 percent of the poverty level, well above what they
would have received from AFDC and food stamps, while others received as little
as 50 percent of the poverty level. Some experimental groups faced benefit
reduction rates of up to 80 percent, which would have been higher than the
benefit reduction rates faced by at least some households in the control groups.
Other experimental groups faced benefit reduction rates of as little as 30
percent, which would have been lower than those faced by the control groups.
Still, according to analysis of the data presented in Burtless’ Table 4, the
effects of changes in each parameter, taken separately, appear to be broadly
consistent with the theoretical model presented in Part 1 of this series:

For both intact families and single heads of household,
groups facing a 75 percent benefit reduction rate under the NIT exhibited
greater average labor withdrawal than those facing a 50 percent rate.

For both intact families and single heads of
households, groups with higher guaranteed minimums had a greater reduction
in work hours.

Husband-wife families showed a greater reduction in
work than single parent families, which is what we would be expect if the
control groups of the single parent families were more likely to be on
welfare plans with high benefit reduction rates.

Unfortunately, these findings are
clouded by methodological flaws in the IMEs. An overview
of the findings of the Boston Fed conference points to numerous problems with
design, execution and analysis, including inadequate theoretical models, poor
formulation of objectives, and unsatisfactory management and administration.
These methodological problems cast doubt on whether evidence from the IMEs
really meets the “gold standard” characterization.

The most important problem was
apparently widespread underreporting of work effort by participants in the
experimental groups. To quote Burtless,

Several analysts have found evidence
that at least part of the employment and earnings reduction reported in the
experiments was spurious. Recipients of negative income tax payments had a
clear incentive to underreport their employment and earnings, because to do so
permitted them to receive a larger payment than the one to which they were
legally entitled. Wage earners enrolled in the control group did not face this
kind of misreporting incentive.

Burtless goes on discuss studies
that use other data sources, including IRS records, to correct the reporting
bias. In the Gary experiment, underreporting appears to have accounted for all
of the negative work response. In the Seattle-Denver experiment, underreporting
did not greatly change the work response of heads of households, but the
reported reduction in hours disappeared for secondary workers.

In an invited response to Burtless’
paper, Orley Ashenfelter of Princeton University notes that a failure to
address the problem of underreporting in advance represented a serious design
flaw of the IMEs:

Only an experiment fully informed at
the design stage about the possibility for income underreporting, and that tested
for its effect, would shed any light on this critical issue. Sadly, the design
of none of these experiments was so informed.

By ignoring the evidence of
underreporting, critics like Manzi and Gobry overstate the case not only
against a UBI, but also against an NIT. As if that were not enough, they
compound the overstatement by implying that the observed work reductions
represented withdrawals from the labor force. For example, Gobry maintains that
as a result of a BIG in any form,

millions of people who could work
won't, just listing away in socially destructive idleness, with the
consequences of this lost productivity reverberating throughout the society in
lower growth and, probably, lower employment, in a UBI-enabled vicious cycle.

Instead, according to research cited
by Dylan Matthews
in a recent post on Vox, even among participants in the IMEs who reduced their
hours worked, full withdrawal from the labor force was a relative rarity.
Instead, the reduction in hours worked more often took the form of longer
periods of job search between spells of employment. For some that might mean
loafing, but for others, it could well mean a more thorough search process
resulting in a better job match. In the case of young secondary workers in
families receiving NIT benefits, reduction in work often meant more time spent
in school. As one participant
in the Boston Fed conference reported, the probability of graduation from high
school was 25 to 30 percent higher in families receiving the NIT than in the
control group.

Structural evidence

So far, we have discussed evidence
in the form of direct observation of labor force participation and hours
worked. Another approach is to use so-called structural models to
estimate elasticities of work effort in response to changes in income and net
wages, that is, wages after benefit reductions and taxes. The income
elasticity of work supplied tells us the percentage by which hours worked
change in response to a one percent change in income, assuming that the net
wage does not change. The substitution elasticity tells us the
percentage by which hours worked change in response to a one percent change in
wages.

Elasticities are important because,
as we pointed out in Part 1, theoretical conclusions about work effort are
subject to the caveat that, other things being equal, the effects of a change
in the minimum income guarantee or benefit reduction rate of a policy would
depend on the strength of the income and substitution effects.

The IMEs themselves are one source
of data for making structural estimates of elasticities. Burtless summarizes
several such estimates in Table 3 of his paper. Estimates of the income
elasticity of work effort for women in IMEs ranged from -.07 to -.15, averaging
about -.12. The range of substitution elasticities for women was from .11 to
.24, averaging .17. For men, the income elasticities ranged from -.075 to -.11,
averaging about -.09, and the substitution elasticities were tightly grouped
around .085.

There is also a large literature
estimating work responses based on nonexperimental wage and income data drawn
from surveys of work behavior, tax records, and other sources. A recent working paper by Robert McLellan and Shannon Mok of the Congressional
Budget Office summarizes the findings. Generally, the income and substitution
elasticities are of the same order of magnitude as those estimated from IME
data. For men and unmarried women, substitution elasticities tend to fall into
a range from 0.1 to 0.3 and income elasticities from 0 to –0.1. For unmarried
women, the substitution elasticity ranges from 0.2 to 0.4 and the income
elasticity from 0 to -0.1.

Some studies also estimate an elasticity
of participation, that is, the change in the percentage of a given
population that would participate in the labor force in response to a change in
the net wage. The CBO working paper considers a participation elasticity of
0.25 to be typical. That would mean that we could expect the participation rate
to increase by about 2.5 percent for each 10 percent increase in the wage. For
example, changing from welfare with a benefit reduction rate of 50 percent to
an UBI with no benefit reduction would increase the net wage by 100 percent. If
the elasticity of participation were .25, we would expect a 25 percent increase
in the participation rate. For example, if 60 percent of welfare recipients
worked before, we would expect 75 percent to work after introduction of the
UBI.

Other studies estimated elasticities
for upper and lower income groups. One study found that the participation
elasticity for the bottom 10 percent of the income distribution was twice as
high as that for the middle of the distribution. Another study found that the
participation elasticity for single mothers was 0.4, higher than the estimation
of .25 for the whole population. Still another study found that for low-income
groups, the elasticity of labor supply with respect to unearned income (which
would include UBI benefits) was only -.04 for women and -.01 for men.

One final type of type of study is
worth mentioning: Some economists have taken advantage of “natural experiments”
to investigate how people react to large increases in windfall income. For
example, a study of Massachusetts lottery winners found that people did not typically retire to a life of
idleness even after receiving very large prizes. On average, each $1,000 of
prize money caused people to reduce their earnings by only about $110. Another study
estimated the effects of inheritances on the work effort of Michigan residents.
By and large, inheritance caused only small changes in work effort. Neither of
these studies lends any support to the notion that a UBI grant of a few
thousand dollars a year would cause massive defections from the labor force.

For readers who are not be used to
thinking in terms of elasticities, it may be helpful translate the estimates we
have cited into some hypothetial examples. The examples assume that we start
with a welfare sysem that guarantees $10,000 for a family of two that has no
earned income, and has a benefit reduction rate of 50 percent. We then replace
that with a UBI that has a basic benefit of $4,000 per family member and no
benefit reduction. For simplicity, all of the examples assume that there are no
other income or payroll taxes, and all use elasticities at the midpoint of the
ranges reported in the CBO working paper.

Jane is a single mother, on welfare, with one child.
She initially works 1,000 hours per year at a wage of $8 per hour. Her
$10,000 maximum benefit is subject to a reduction of $4,000 because of her
earnings, so her disposable income consists of $8,000 of earned income
plus $6,000 of benefits, net of reductions, or $14,000 in total. Another
way to look at it would be to say that her net wage is $4.00 per hour,
after benefit reductions. Under the UBI, her benefit would be $8,000, not
subject to reduction. If she worked the same number of hours, her
disposable income would be $16,000 ($8,000 UBI benefit + $8,000
earnings)—a 14 percent increase. With an income elasticity of work effort
of -.05, a 14 percent increase in income would cause a .7 percent decrease
in desired hours worked, or 7 hours per year. At the same time, by
eliminating the 50 percent benefit reduction, the UBI would increase
Jane’s net wage from $4.00 per hour to $8 per hour—a 100 percent increase.
With an elasticity of substitution of .3, the UBI would induce a 30
percent increase in desired hours worked, or 300 hours per year. Taking
the two effects together, total work hours would rise by 293 hours. On
balance, then, replacing the current welfare system with a UBI would
increase Jane’s net income from $14,000 to $18,344 ($8000 (UBI) + $8 X
1293 hours). Her total income and hours worked would both increase.

David, a middle-class professional in a traditional
marriage to a nonworking spouse, no children, earns $60,000 per year after
taxes, a little above the median household income. He works 2,000 hours
per year. The UBI does not change his net wage, so it has is no
substitution effect, but it raises his disposable income by 13 percent, to
$68,000 per year, or 13 percent. Applying an income elasticity of -.05
means that he would reduce his desired hours of work by about .65 percent,
or 13 hours per year. However, if, as I have suggested elsewhere,
the UBI is financed in part by eliminating middle-class tax loopholes
(without changing marginal tax rates), Dave’s income would increase by
less than the full $8,000 and he would reduce his annual work by less than
13 hours.

Bruce, a single 20-something, is not eligible for any
welfare programs. He lives on an old boat, gets by without health
insurance, and makes enough to meet his basic needs by working 800 hours a
year doing odd jobs at $10 per hour. He spends his spare time watching
birds and playing the guitar with friends. With the UBI, his income would
jump to $16,000 per year, a 100 percent increase. Applying a typical
income elasticity of -.05, we would expect him to cut his work back 40
hours per year. However, the -.05 is just an average. Maybe Bruce is not
typical. Maybe he would be prefer to continue his $8,000 a year lifestyle,
not working at all, and spend 800 more hours a year on birds and music.
The UBI would allow him to do so if he chose.

These are hypothetical examples, but
they illustrate a key point: The income effect of a UBI, which discourages
work, is weak, whereas the substitution effect, which encourages work, is strong.
One reason for the relative weakness of the income effect is the simple fact
that the absolute value of the income elasticity is less than that of the
substitution elasticity—a finding common to nearly every statistical study of
work behavior. The other reason is that for most people, a UBI of the kind I
have described causes a relatively small percentage increase in income, when we
take prior earnings and welfare benefits into account.

Given a weak income effect and a
strong substitution effect, there is only one case in which a UBI can cause a
large decrease in work effort, let alone complete withdrawal from the labor
market. That is to posit a person like Bruce, who initially receives no income
support benefits at all, who is not just able to live on a very low income but
enjoys doing so, and who has an income elasticity that is far greater that the
population average.

Most people can probably think of at
least one person they know, or have heard of, who fits the “Bruce” profile.
Anecdotal evidence is powerful, and people are quick to extrapolate from a
couple of guitar players spotted in their local park to millions of Bruces
“listing away in socially destructive idleness.” However, bear in mind that
actual data from the IMEs, from econometric studies of labor market behavior,
and from “natural experiments” like lotteries and inheritance uniformly
indicate that, when it comes to population averages, there just aren’t enough
Bruces to outweigh the effects of the tens of millions of Janes and Daves.

The bottom line

In the two parts of this series, if
have argued that standard economic theory and available empirical evidence
support the idea that a well-designed and properly financed UBI, introduced as
a replacement for our current welfare system, would be more likely to increase
than to decrease average work effort for the population as a whole.

I have also questioned the
conclusions some critics have drawn from the income maintenance experiments of
the 1970s and 1980s. In doing so, however, I don’t intend any blanket criticism
of the experimental approach. On the contrary, I think that a randomized field
trial of a true UBI, conducted along the lines of the IMEs of earlier years,
could help resolve some of the outstanding issues. A recent Republican proposal,
Expanding Opportunity in America, calls for using some funds now allocated to federal
welfare programs to fund state-level experiments with new ideas. The initial
draft of the proposal specifically barred experiments with a UBI or any other
policy that did not include a work requirement, but we can hope that is not the
last word.

Meanwhile, the theoretical analysis
and indirect evidence that we do have remains largely supportive of the
proposition that a UBI would have a favorable impact on work incentives.

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